My department is in the middle of a faculty search right now, with the result that we’ve had several job candidates deliver talks in the last couple of months. The talks have been uniformly clear, well-delivered, and polished. Based on the research and future directions, most of the candidates seem to be well-positioned to start up research programs and land a couple of grants. This is all very impressive.
But in one respect I have found the talks slightly disappointing. By and large, the candidates have not described future directions that were surprising. By that I mean that no one has carved out a scientific niche for him or herself that seems distinct from the territory occupied by other people in the field.
For example, one speaker alluded to papers that had come out from competing groups around the same time as his most recent paper. These competing groups had been studying marginally different types of cells, so nobody was technically scooped, but it struck me that if this candidate were to have a piano land on his head tomorrow, there would still be plenty of people pursuing the types of questions that he plans to pursue.
I voiced this concern to some lab colleagues who told me that I was being too critical, and that nobody occupies unique scientific space and therefore this was an impossible standard. And of course a PI can compete with others in the field and still excel--and it’s even a mark of the importance of the field, in some respects, that there's so much interest in it.
Yet when I think about faculty whose work I consider singularly exciting, many of them have either developed techniques that let them answer questions no one else in their field has been able to attack, or they have devised a research program that addresses questions--frequently at the intersection of two separate fields--that nobody else is pursuing.
There’s still time for these junior candidates to grow into those shoes, but I’m left wondering if their feet are going to get any larger.
15 years ago
12 comments:
Is it really possible, in this day an age, to have one's own niche to own? To have one's own funded niche, it seems that would be near and far anymore, at least from my stand point in science.
I think your instinct is right. However, I don't think that it's necessary for one to be working on something completely different from everyone else to be in their own niche. Some of the greats in my field have tackled problems in progress by others (sometimes many others) but saw it in a new way or put their own spin on the question in such a way to make the problem a new one. I think the ability to take a known problem and solve it differently or find something new in it is a great way to make an impact. Did any of the candidates talk about how they approached their research problems differently than their competitors or talk about unique interpretations of existing data or otherwise show this kind of uniqueness?
and it’s even a mark of the importance of the field, in some respects, that there's so much interest in it.
whaddaya mean 'naked'? Those are some mighty fine robes the Emperor is sporting. If you cannot see the Glamour of that raiment you are just an unsophisticated country rube. be off, ruffian!
Leading off with the disclaimer that the funding mechanism for intramural research at NIH is quite different from that for extramural research...
I had a long conversation with an investigator at NIH-who's been there a looonnnng time-and we discussed his approach to research. In his view, if he died today and the field carried on just the same tomorrow (because some other lab was doing the same research), then he was doing it wrong. It might sound kind of egotistical, but he felt that if your research is truly having a major impact on your field, then the loss should be evident when you're no longer there.
I'm surprised, Anon1, that you think it's that hard to think of under-explored territories and/or distinctive approaches to old territories. Obviously, once you start pursuing something, others are likely to jump in as well. But I'm with the PI biochem belle talked to--it's hard to believe that one's contribution is significant if there are already twelve other labs doing the exact same thing.
Anon2, the idea was that most of them would have new technical approaches. However, their new technical approaches are all the same as each other's, which makes it hard to sound particularly unique...
...but it struck me that if this candidate were to have a piano land on his head tomorrow, there would still be plenty of people pursuing the types of questions that he plans to pursue.
The fact that there are so many people that will want to pursue the same topic; does this not suggest somehow that the topic is important and worth pursuing?
I am on the job market for TT assistant professor this year, and I chose not to mention a couple of topics that I am also interested in, because no one cares about them, there is no funding, and that field is as good as dead.
Carving out a niche for yourself in something that no else wants to work in is a luxury that only fully tenured faculty can afford. Unfortunate, but absolutely true.
The fact that there are so many people that will want to pursue the same topic; does this not suggest somehow that the topic is important and worth pursuing?
Sure, as I wrote in the original post. However, it's not clear that it's worth hiring somebody to pursue it if that person demonstrates little to no intellectual capacity for generating independent, interesting, unbeaten-path ideas.
Of course you write grants on more well-trodden areas. That doesn't mean that's the only stuff you should be pursuing, though. I am not talking about old dead topics that nobody else is interested in, as you are; I am talking about topics that you specifically create yourself, by bringing a new perspective or question to an area.
If you can't come up with interesting questions that no one else has established major research programs in, perhaps science is not the right field for you.
I agree with your last comment Dr. J. I have been sitting in on 2 searches this year, so I have been thinking about this issue. All of the candidates are planning extensions/new directions branching from their prior research, which is normal. But what really separated the great candidates (who I would love to hire) from the good candidates (who gave nice talks about interesting science for the most part) is in their future plans.
The really great candidates spoke about some unique and interesting twist, angle, or side project they planned to pursue. The best of these were clearly intended as second projects after some funding was obtained, since they tend towards the risky as brand new lines of inquiry. On one search, we outright asked "what is your angle?" to all of the candidates, and I was surprised by how many couldn't answer it.
There are lots of unrecognized niches, but noticing them does take creativity and thinking at the intersection of the standard problems. I have such a niche, I developed it (discovered it) before I started applying for jobs, and I've been generally successful at getting funding.
A lot of people working on something suggests it's interesting. But it also suggests that in order to do well, you're going to have to come up with better ideas than a lot of other very smart people. If you're going to follow the crowd like that, you better have something that gives you an edge. Raw intelligence isn't going to cut it.
HAHAHA! Great post and interesting comments.
I have a completely unique research area at the intersection of two fields. If a piano dropped on my head (as it kind of already has), several aspects of my research would disappear for twenty years until someone rediscovers them.
This is precisely why I can't get a job. Too unique! Too risky!
Departments don't want someone with a different point of view. They want someone who reminds them of themselves: someone who FITS IN and does what everyone expects.
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